July 27, 2009

Selecting another polymath project

In a few months (the tentative target date is October), we plan to launch another polymath project (though there may also be additional projects before this date); however, at this stage, we have not yet settled on what that project would be, or even how exactly we are to select it. The purpose of this post, then, is to begin a sort of pre-pre-selection process, in which we discuss how to organise the search for a new project, what criteria we would use to identify particularly promising projects, and how to run the ensuing discussion or voting to decide exactly which project to begin. (We think it best to only launch one project at a time, for reasons to be discussed below.)

There are already a small number of polymath projects being proposed, and I expect this number to grow in the near future. Anyone with a problem which is potentially receptive to the polymath approach, and who is willing to invest significant amounts of time and effort to administrate and advance the effort, is welcome to make their own proposal, either in their own forum, or by contacting one of us. (If you do make a proposal on your own wordpress blog, put it in the category “polymath proposals” so that it will be picked up by the above link.) There is already some preliminary debate and discussion at the pages of each of these proposals, though one should avoid any major sustained efforts at solving the problem yet, until the participants for the project are fully assembled and prepared, and the formal polymath threads are ready to launch.

[One lesson we got from the minipolymath feedback was that one would like a long period of lead time before a polymath project is formally launched, to get people prepared by reading up and allocating time in advance. So it makes sense to have the outlines of a project revealed well in advance, though perhaps the precise details of the project (e.g. a compilation of the proposer’s own thoughts on the problem) can wait until the launch date.]

On the other hand, we do not want to launch multiple projects at once. So far, the response to each new launched project has been overwhelming, but this may not always be the case in the future, and in particular simultaneous projects may have to compete with each other for attention, and perhaps most crucially, for the time and efforts of the core participants of the project. Such a conflict would be particularly acute for projects that are in the same field, or in related fields. (In particular, we would like to diversify the polymath enterprise beyond combinatorics, which is where most of the existing projects lie.)

So we need some way to identify the most promising projects to work on. What criteria would we look for in a polymath project that would indicate a high likelihood of full or partial success, or at least a valuable learning experience to aid the organisation of future projects of this type? Some key factors come to mind:

The amount of expected participation. The more people who are interested in participating, both at a casual level and at a more active full time level, the better the chances that the project will be a success. We may end up polling readers of this blog for their expected participation level (no participation, observation only, casual participation, active participation, organiser/moderator) for each proposed project, to get some idea as to the interest level.

The feasibility of the project. I would imagine that a polymath to solve the Riemann Hypothesis will be a spectacular and frustrating fiasco; we should focus on problems that look like some progress can be made. Ideally, there should be several potentially promising avenues of inquiry identified in advance; simply dumping the problem onto the participants with no suggestions whatsoever (as was done with the minipolymath project) seems to be a suboptimal way to proceed.

The flexibility of the project. This is related to point #2; it may be that the problem as stated is beyond the ability of the polymath effort, but perhaps some interesting variant of the problem is more feasible. A problem which allows for a number of variations would be more suitable for a polymath effort, especially since polymath projects seem particularly capable of pursuing multiple directions of attack at once.

The available time and energy of the administrator. Another thing we learned from the minipolymath project was that these projects need one or more active leaders who are willing to take the initiative and push the project in the directions it needs to go (e.g. by encouraging more efforts at exposition when the flood of ideas become too chaotic). The proposer of a project would be one obvious choice for such a leader, but there seems to be no reason why a project could have multiple such leaders (and any given participant could choose to seize the initiative and make a major push to advance the project unilaterally).

The barriers to entry. Some projects may require a substantial amount of technical preparation before participation; this is perhaps one reason why existing projects have been focused on “elementary” fields of mathematics, such as combinatorics. Nevertheless, it should be possible (perhaps with some tweaking of the format) to adapt these projects to more “sophisticated” mathematical fields. For instance, one could imagine a polymath project which is not aimed at solving a particular problem per se, but is instead trying to understand a difficult mathematical topic (e.g. quantum field theory, to pick a subject a random) as thoroughly as possible. Given the right leadership, and sufficient interest, this very different type of polymath project could well be a great success.

Lack of conflict with existing research. It has been pointed out that one should be careful not to let a polymath project steamroll over the existing research plans of some mathematician (e.g. a grad student’s thesis). This is one reason why we are planning an extended process to select projects, so that such clashes can be identified as early as possible, presumably removing that particular project from contention. (There is also the danger that even a proposal for a polymath project may deter other mathematicians from pursuing that problem by more traditional means; this is another point worth discussing here.)

Over to the other readers of this blog: what else should we be looking for in a polymath project? How quickly should we proceed with the selection process? Should we decide by popular vote, or by some fixed criteria?

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As I said on my blog, I have a document with ten proposals (some of which I’ll hold back for a while — I don’t want to swamp people with too many proposals). I gave each one ratings according to six criteria, which are similar to yours above, but not identical. So let me reproduce here what I wrote:

(i) Does the problem have the potential for direct and incremental progress?

I believe that all problems, once one starts to think about them, can be solved by means of gradual processes rather than by the sudden arrival of a spectacular idea. (Such ideas do occur, but the groundwork has to be laid in advance.) However, there also seems to be a spectrum. Some questions seem not to be amenable to current techniques: if they are solved, it may well be as a result of good fortune, such as somebody developing an idea in connection with another problem and that idea turning out to be useful for the original question. Polymath is probably better suited to problems that can be solved by a more direct route: you just set out to solve a particular problem and hope that you do in the end solve that problem. (But of course it could happen that you set out to solve a particular problem and end up solving something else — that too seems quite a likely outcome.)

(ii) Does the problem have a computational side?

A lesson from the DHJ experience was that there were very different ways that people could contribute. In particular, there was a clear distinction between people who were primarily interested in the question as a theoretical problem, and people who enjoyed looking at small cases, possibly with the help of a computer, and obtaining exact results. In my opinion, it is an advantage for Polymath if a problem can be studied experimentally as well as theoretically.

(iii) Does the problem have the right level and kind of difficulty?

I think the ideal level of difficulty is a problem that is known to be hard but not in any sense “known to be impossible”. Sometimes when one attacks a problem, one comes up with a very solid theoretical reason to believe that it is difficult. For instance, there might be a convincing argument that the correct approach for attacking the problem is to use deep tools from some area, and it might be that what is needed from those tools is stronger than what is known. But sometimes one just gets exhausted by a problem and is left feeling that with a bigger push it might be possible to solve it. The latter kind of problem ought to be ideal for Polymath.

(iv) Is it realistic to tackle the problem by elementary means?

I do not rule out problems that need a certain amount of knowledge and technical expertise, but I regard that as a disadvantage, since it reduces the pool of potential participants.

(v) Is the problem widely acknowledged to be interesting?

I don’t want to propose that several people put in a lot of effort to solve a problem unless there are plenty of people who would be very interested to see a solution.

(vi) Is there a danger of adversely affecting the career of a young mathematician?

Some problems are sufficiently well known that they count as public property. Others might be the topic that a PhD student has been working on for two years. It often happens that mathematicians “lose” a great deal of effort when somebody else solves a problem on which they have been working. However, it would be good to minimize the chances of this being the result of a Polymath project.

Just to get the ball rolling, here is a suggestion for how a selection might take place. Initially, some reasonably short proposals are put up and discussed. Then, as a result of the discussion, a shortlist is drawn up — possibly with the help of a vote if that seems necessary — and more details are given about the shortlisted proposals. Then the advantages and disadvantages of these proposals are discussed, and we get some sense of who potential contributors might be, how much interest there is, and so on. Finally, a vote is taken, but instead of people simply putting proposals in order of preference, they do something a bit more informative, such as indicating for each proposal how much they would be likely to participate if it was the chosen project. Speaking for myself, I know that in order for me to work properly on a problem, something has to happen to get me hooked. Usually it’s a combination of its being sufficiently in my area for me to feel I can have a go, and my having thought about it enough to have at least some ideas, however small and unlikely to form part of an eventual solution. A polymath proposal that I don’t get hooked by is one that I will probably end up not contributing to all that much. That is not to say that it shouldn’t happen, but I sort of hope it won’t happen for the next project.

Another thought is this. When projects are proposed, we could have a mechanism for people to sign up as serious participants. I define a serious participant (there may be a better phrase) as follows. It is somebody who is sufficiently gripped by the problem, and sufficiently knowledgeable and experienced, to be able and willing to spend the time needed to keep up with the posts, and to contribute to the posts as well. This could even be part of the data that people have available before a vote takes place — that is, some sense of who the participants would be.

A polymath project to understand some difficult subject thoroughly might fruitfully be organized in parallel with (or perhaps slightly before) a more problem-oriented polymath project in a similar area. I’d find this interesting for the prime-generating problem, for example. In a sense, this would scale up and systematize Terry’s DHJ reading group. It would also provide a natural way for people with less expertise to participate, and the more devoted might “graduate” to full-fledged participation in the problem-solving effort.

I agree. And I have a related proposal, which is that when it is decided what the next project will be, if it is one that involves a certain amount of understanding before one is up to speed, there should be a discussion of this kind. If we were doing DHJ now, I would propose that a lot of the wiki material (things like proofs of Sperner’s theorem, Roth’s theorem and the corners theorem) should be well-developed so that people had the opportunity to familiarize themselves with the kinds of arguments that the main eventual participants knew thoroughly. And in parallel with that, there would be plenty of opportunity for people to ask questions of the main proposer (and for others to answer those questions if they want to). I think that quite a long time — a month even — would be suitable for this.

[Small technical point — I’ve just replied to the wrong comment. I find having the information about a comment appearing at the bottom of a comment quite confusing. Is it possible to adjust the theme so that that stuff appears at the top?]

I agree that more of a push to widen the accessibility of the DHJ project would be a good idea. It may be difficult to hold back the research side of things, though. For instance, for the finding primes project, I’m now scrambling to put into place the other aspects of the polymath paradigm even though we haven’t officially launched it yet, due to the non-trivial amount of progress made so far; ideally we should have some wiki notes on pseudorandom number generators, Cramer’s conjecture, etc. before we start but I guess this will have to be created on the fly (and we may have to launch this particular project ahead of schedule if the pace picks up any more).

I think one can adjust the positioning of the comment metadata by editing the CSS, but don’t know exactly how; I’ll pose this question in the formatting thread in the hope that a CSS expert comes along to read it.

It is not clear to me that the possible audiences of different “polymath” projects are the same. One could think of concurrent ongoing projects aimed at (nearly) disjoint sets of participants. (E.g. a polymath project in Algorithmic Game Theory will probably have a pretty low overlap with any of the projects proposed here)

Another thought about the selection process is that it might be better to select not one but four or five projects that we definitely intend to go ahead with. I don’t mean by that that we would start them all at the same time — far from it — but simply that we wouldn’t have a new vote every time we felt that a new project could be supported. That would have the advantage that preliminary work, such as setting up useful resources on the wiki, could be done more thoroughly before the later projects started.

I think the “polymath ethic” needs to be adapted for selecting problems. Basically, selecting comments requires both wide expertise, considerable off-line thought (such as done by Tim or Gil with their proposals), as well as consultation with outsiders on behalf of the project. It is a “global optimization” issue, unlike the solution which involves many “local” steps. Thus my guess is thus that it would be better for some kind of “committee of experts” [self-selected by participating in a comment thread] to do this, probably involving the “guardian council” of Gil, Terry, and Tim.

To extend a comment on the deterministic prime-finding thread, it would be good to distinguish between NP-Poly Projects (whose objectives are in NP, but whose success in uncertain) as contrasted with P-Poly Projects (which are pretty guaranteed to succeed, with sufficient resources, diligence, and skill).

It is easy to think of historical examples of P-Poly Projects … they include some of humanity’s most lustrous scientific enterprises … the Genome Project … the Apollo Project … the Manhattan Project … the Large Hadron Collider … and hopefully even large P-Poly Projects will be launched this century.

It seems to me that it is the P-Poly Projects that have the most scope for creating jobs and careers on the scale that our planet (not to mention our respective academic disciplines!) urgently requires.

For me, the very best posts on the blogs of Nielsen, Tao, Kalai, Gowers (and Fortnow/GASARCH too) are those that touch upon this theme.

I guess there is a _de facto_ project of this sort going on at your blog and at Lipton’s blog. But I do like the idea of putting some polymath resources behind it; we’ll have to talk with the various people involved for this of course.